(upbeat music)
- I think the main way to determine what experiments need to
do is to write down what questions you're trying to answer.
One you write down whatever type of question
you're trying to answer if you look in the literature
and see how would I answer this question,
what experiments kind of mimic what I want to do,
what I'm trying to get at?
Once I do that, then I'm like
oh this is definitely the next step.
When I'm looking at mice, how do I design
an orthotopic xenograph model?
How do I look at breast cancer development in mice?
How do I look at human breast cancer cells
being colonized in the lung?
How exactly do I look at that experiment?
I think the main thing is reading the literature,
trying to figure out what experiment I'm trying to do
from the literature and seeing how does that fit
into the context of what I'm studying.
- When you're trying to figure out an experimental strategy
it's worth while to remember that even though
we think that there are a lot of different
kinds of experiments, they actually fall into some
pretty straight forward categories.
In general if you can think about what
are my pertubation tools, what are my measurements
that I can make, what's the time scale
at which I can make those measurements,
and in how many individuals can I make those measurements?
I think it can be really useful
to break things down in that way.
What are my perturbation tools?
For instance, you can break the components
and measure what happens, over express or augment
the activity of the components and see what happens,
look at natural populations and how they are different
from one another in whatever feature you want to look at.
Those things map on different systems in different ways.
Ask yourself what are you going to measure?
Are you going to measure a molecular phenotype
or are you going to measure an organismal phenotype
like behavior or a developmental character
or something like that.
Once you think about that, what's the timescale
at which I can make those measurements?
Are you going to measure it continuously over time
in a single case or are you going to measure it
statistically at one time over lots of individuals
and what are the caveats of doing both of those things
in those two ways.
There's usually a trade off somewhere between
the through put with which you can do something
and the resolution with which you can do it.
Then ask in how many individuals
can I make those measurements?
Be they individual cells or individual organisms.
That's sort of how's the material processed
such as am I looking at single events
or am I looking at average cohort
either over space and time.
The cam help you whittle down what techniques
are available to you in each one of those cases.
- We have a classification system in my laboratory
for three kinds of experiments and results.
Class one experiments are those where
either answer is interesting.
They're actually relatively rare to find class one.
Most of the experiments that we do
are what we call class two
where usually only the positive result is meaningful
and the negative result doesn't actually move the ball.
It's really important to know the distinction
between class one and class two.
If you get it wrong, you start chasing
negative results that you think are meaningful
but are not.
You can really go off in the wrong direction.
Class three experiments of course are those where
neither answer is interesting and informative.
They're to avoided at all costs.
What would a class one experiment look like?
One kind of experiment is to be descriptive.
That challenge of then deciding
which characteristics will we look at,
how broadly will be catalog them,
will it just in one cell type and so forth.
Are all decisions that need to be made
but you can see that the experiments are class one.
It doesn't matter if there's a methylation on this histone
at that position, you just want to know if it's there or not.
And under what conditions is it there versus not there.
It's all informative, it's all class one.
It's really important in planning of every experiment
to ask if this class one, two or three?
- This is going to sound very self-critical,
I wish I would have known the extend of my own laziness
in terms of doing science because basically the way
I approached grad school was using the tools
that I've already been developed in the lab
and applying them to specific projects.
I wish I had been more open to considering
new types of measurements and techniques earlier
because the window of opportunity
for incorporating new skills into your research repertoire
shrinks over time as you try and zero in on a project
and get it done in order to graduate.
In not being adventurous, I missed out on the opportunity
to do the right experiments at the right time.
Looking at a given project, you can attack it from
different angles all the time.
You basically choose the angles that you think
are best scientifically and experiments
that you think you can perform.
Those are the two variables that you kind of optimize.
It's the second one that's the key.
The ones that you think you can perform.
If you are exposed to lots of different techniques early on,
then you're not longer limited by that
and can perform any experiment,
especially the one that you absolutely need
to further the project at a given time.
I think that's really important to keep in mind.
As you broaden yourself out early on,
it will help you attack the right experimental questions
as you continue in your project.
- I think the most important part of
picking and choosing from existing techniques
or developing new ones is to understand what your investment
in doing something new is going to get you.
In this sense what you really want to do
is kind of black box the technique.
You want to think if I could do this thing
and I'm going to black box it,
I don't know how you do it at all.
But if I could feed this thing into it
and get this thing out of it,
then I would be able to learn what?
What would be the great value here?
I'm a big believer in the fact that
as scientists we should communicate openly with one another
and share tools and resources.
Because that maximizes our investment in science as a whole.
There's no reason for us to duplicate efforts
if we don't have to.
In that sense I'm very reluctant to invest
technically in methods that I think
would be appropriate for us to use
if somebody else is already doing them.
- In making progress on a research question
after your convinced that the system is working
and you can make some good measurements,
I think it's important to start
writing papers in your head.
Or at least thinking about what set of
possible figures would constitute a paper
that people would be excited to read.
In doing that it points you to experiments
and also holes in existing experiments
that you can follow up on
and fill over the course of your graduate career.
I recommend it as a tool in terms of
conceptualizing your project and its direction.